Home > Research > Are your research aims the right aims?

Are your research aims the right aims?

Defining the aims of a research project, whether it be for a Masters or PhD thesis, or even a major grant application, requires considerable thought. It is more difficult than it looks for several distinct reasons.

First, one must define a general research area in which to work.  The hardest part about research is finding the right problem to work on.  The problem needs to be hard enough and interesting enough for others to recognise the value of your contributions.  Yet if it is too hard, it would not be possible to make a sufficiently worthwhile contribution in a reasonable amount of time. Several common strategies are:

  • The entrepreneurial approach. Identify a problem that has not been considered yet by your peers but which you believe will attract attention once people become aware of it. Looking backwards, it is easy to identify areas of work which were (or are) a hot topic and for which the barrier to entry was not great; it was the right problem at the right time to consider.
  • The arbitrage approach. Different disciplines can have different approaches for tackling similar problems; it is not uncommon for one discipline to be completely unaware of related advances in another discipline. Look for how your expertise can be applied outside your discipline in a novel way.  (Breakthroughs in an area often come about by the introduction of ideas originally foreign to that area.)
  • The team approach. Find a world-class team of experts working on a grand challenge problem and join them.  This has many benefits.  It will serve as a constant supply of interesting research problems to work on and your research will have greater impact because the team as a whole will work towards consolidating contributions into even bigger ones.
  • The tour de force approach. Keeping in mind that even great research is the result of 1% inspiration and 99% perspiration, if you have the determination and single-mindedness to spend many months chipping away at a difficult problem, chances are that you will be rewarded.

Next, it must be appreciated that identifying an area in which to work is just the first step in defining your research aims.  Wanting to develop a better algorithm for a certain signal processing problem is not a tangible goal that you can work towards unless you have defined what you mean by better.  It is not uncommon for this step to be omitted, with the hope that a new idea will lead to a new algorithm which will be found serendipitously to have some advantage over previous approaches. Yet there is little to recommend this rush-in approach since invariably the small amount of time saved at the beginning is more than lost by the lack of focus and direction during the remainder of the project. Furthermore, few funding agencies would be willing to fund such a cavalier approach, just as few investors would be prepared to invest in a start-up without a business case. It might succeed, but experience suggests it would be a bigger success if time is invested up front to think carefully about what it is you really want to solve.  Measure nine times, cut once.

Research aims should be:

  • Tangible and measurable. An independent person should be able to come along and judge whether or not you have made significant progress.
  • Outcome focused, not output focused. Writing reports and journal papers are outputs, but if no one uses or builds on your work, you have not achieved an outcome.
  • Achievable. You must be able to give a credible argument as to why you will be able to achieve your aims in the allocated time frame.
  • Hierarchical. A hierarchical structure allows for ambitious aims at the top level with shorter-term goals leading up to them. This is generally seen to be:
    • focused and efficient – your work builds on itself and grows into something substantial rather than remaining a diverse collection of less substantial contributions;
    • mitigating risk – by having lower level aims which are perceived as achievable then there is less concern that you may not achieve all of your more ambitious aims;
    • outcome orientated – focused work on ambitious  (and appropriately chosen) aims is perhaps the best way of maximising the potential outcomes and impact of your work.

Supporting the research aims should be statements on the significance and innovation of the proposed research and an explanation of the approach and methodology which will be adopted.  All this should be described in the context of previous and current international work in the relevant areas.

  1. Xi Liang
    July 8, 2010 at 10:30 am

    I am a Masters by reseach student in CSSE department. I read this article several times since you publish it. I found it is very helpful and re-exam my progress and framework of the whole project every time when I read your article.

    I have been doing my Masters for 14 months and currently writing my conversion report. It is the first time when I really think about what will be the “outcome” of the project of PhD, how I will achieve it step by step, what are the main challenges, and what main contributions we will make, and how to make a practical timeline or plan to make sure my research is on the right track.

    My research project is about tumor cencer detection in breast MRI. It will include several reletive big area of image processing, image registration, segmentation, feature extraction and classification. Each area is a big research topic by itself and also strongly related. At the very beginning of my research study, I have a rough understanding I need to develop algorith
    and code in those areas. But I never really think about how long it will take and how I can chain them up and finally be able to finish my PhD thesis within a reasonable time. Therefore I spent quite long time in automatic image registration algorithm which is Only the pre-processing stage for Tumor detection. After I write up the conversion report , I realize it is not practical for me to generate a reliable and robust automatic image segmentation which is a criticle process before the tumor detection and I can need do manual segmentation.

    The lesion I learn here is a very good understanding of the project objective and an practical plan at the beginning is enssentil. Then the thing left is keep things on track which is a lot easier. I talked with a PhD student who published 5 journal paper and 5 conf paper and finish PhD thesis in three years. He said the secret is he has a very clear idea what he wants all the time.

  2. Michael
    August 3, 2010 at 10:25 am

    Very inspiring.
    –Current 2nd year Mech Eng student at Melb Uni who want to do research

  3. A Research Fellow
    August 30, 2010 at 11:28 am

    Dear Professor, I have benefited from your series of mini-course on statistical signal processing, and now these guidelines. For these, I’m grateful.

    While these guidelines are useful, I wonder if you have any advice to give to researchers of the following nature. They are trained in applications instead of theory. To apply for Discovery Project grants, they lack the necessary theoretical background. To apply for Linkage Project grants, the industry in their area is weak or non-existent. What advice would you give to these researchers to get a piece of the Discovery Project pie?

    I’m not sure if this is a valid question, but I thank you in advance.

    • August 30, 2010 at 5:52 pm

      It is difficult to give an answer without knowing the details of the question; it may well be a case of terminology. Discovery Projects (from the Australian Research Council) look for a rigorous (and ideally novel) approach to a significant (and often practical) problem. The distinction is not between “theory” and “applications”, but rather between “rigorous and informed research” and a “consultancy”. Provided the proposed project does not resemble a consultancy and tackles an important problem in a rigorous and sensible way, it has a chance of being funded. That said, good research is almost always a balance between theory and practice; theory informs, and in turn is informed by, practice. Once the link is seen, learning the theory may become more enjoyable…

      • A Research Fellow
        August 30, 2010 at 8:55 pm

        Dear Professor, I thank you from the bottom of my heart. Your reply is enlightening. I now know how to proceed with the coming funding round.

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